The Meaning of Omega

Andrew Stothers wrote in 2007 a first-year qualifying report for the University of Edinburgh PhD programme. In only eleven pages he presented the parts of the famous paper by Don Coppersmith and Shmuel Winograd (CW) that do enough to obtain for the exponent of matrix multiplication. In a few more pages he surveyed recent work on sufficient conditions for . Page 15, the last except for references, laid out “Possible Directions for Future Work” in five sentences, the fifth being:

Finally, it will also be possible to investigate bilinear algorithms further and use more complex means to determine whether or not “better” algorithms exist for matrix multiplication.

Today we wish to explain what means, why lower is always “better,” why we feel our field is better for the great efforts expended by Stothers and Virginia Vassilevska Williams, and why it is better when intellectual values guide our judgment. We also wish to defend ourselves and others for calling the results “breakthroughs,” comparing and contrasting to recent advances on algorithms for the Traveling Salesman Problem.

I (Ken) wrote a similar first-year qualifier in summer 1982 after my first year at Oxford—they are a staple of leading British universities. Like Andrew’s it was not obligated to have original research, just to demonstrate understanding and capability. One item found its way into a conference paper, but my 1986 dissertation ranged into various other topics.

What distinguishes Andrew’s Nov. 2010 dissertation is its singular focus on accomplishing the objective of his proposal. And doing it. The resulting paper with his advisor Sandy Davie has recently been submitted. Meanwhile in North America, Virginia had been thinking about the same problem since 2005. It may not be true as asserted here that “hundreds of people tried to improve” it after 1987, but we’ll guess about as many people thought about it. It’s enough to note that many researchers felt it worthy of pursuit, including Andrew’s advisor, and that progress took large concerted effort. The nature of this effort—including the use of computers—may be an important harbinger for science by itself.

What Does ω Mean?

The definition of is the infimum of all such that matrix multiplication has an algorithm that runs in time . This is in a classical model of computation where addition and multiplication of scalars have unit cost. Note that there might not be an algorithm that runs in time itself— may properly be a limit even if it turns out to have the least possible value 2. Currently all we know is that from Virginia’s work.

As many have noted, does not have immediate practical relevance because there is evidently a tradeoff with the constant hiding under the in . The tradeoff is so far steep enough that apparently only Volker Strassen’s relatively simple algorithm achieving an exponent of has wide use. So why do we care about values of less than that?

One of the central questions in physics is, why do the fundamental constants of nature have the values they do? The desire for why, in the face of evidence that the values could be arbitrary, has aroused such passion that string theorist David Gross channeled Winston Churchill in exhorting young physicists to “never, never, never give up.”

Now in mathematics it may seem nonsensical to ask, why do numbers like and have the values they do? But with , we are in a sense closer to physics: understanding it is akin to discovering a natural law, at least a law of information. And quantum mechanics has if anything magnified William Hamilton’s vision approaching 200 years ago that Nature computes with matrices, yes large ones. It is possible that detracts from a better statement of important laws, but knowing better brings us closer to them all the same.

Barriers and Breakthroughs

Hence also the interest in whether takes a value with known meaning, such as or (both falsified) or , or as some have mused, or , or as some have argued more likely for exponents, a logarithm of some higher and simpler number. Strassen himself has often stated his belief that is strictly greater than . If it has a value not previously seen in mathematics, then we could hope to discover new mathematical regularities as well; if it has a known value, then this may yield some more explanation about algorithms.

The value seemed a natural possible barrier, but the time interval from to in 1981–82 was very short. By contrast the “CW” bound of was not a natural-seeming number, but it withstood attempts to scale it for 23 years, including a year’s work from each of Virginia and Andrew. Reasons of intellectual judgment, expanded below, we feel are enough to justify calling their final results a “breakthrough.” But we offer a recent concrete case for comparison first.

The Salesman Always Rings 1.5

The Traveling Salesman Problem (TSP) seeks the shortest route to visit each of a given set of sites, coming back in a ring to the starting site. When the sites are in real space and “shortest” refers to Euclidean distance, finding the length of the absolute shortest route remains -hard even in the plane, as discussed here. However, Nicos Christofides in 1976 found a polynomial-time algorithm that finds a tour guaranteed to have total length at most . The method and proof apply to various other cases where the distances between sites obey inequalities that define some kind of metric, with the same bound.

This stood as a barrier for most of these cases, until this year. Shayan Oveis Gharan, Amit Saberi, and Mohit Singh (OSS) broke it for a wide subclass of these problems. Well they “broke” it by achieving a guaranteed ratio to the optimum of

Actually their original paper did not give a value—it merely proved the existence of an giving . The estimate for the magnitude of their breakthrough was supplied later.

Improvements and Predictions

It must be said that the OSS paper and its predecessor introduced techniques that were more novel to the problem than is evident for the new matrix-multiplication papers, and the predecessor won the SODA 2010 “Best Paper” award. However, a referee could have wondered, why bother moving heaven and earth in a restricted case to demonstrate an increment a thousand times smaller than “nano”? Indeed the version of OSS linked above still ends with “” on page 65.

What happened is that the change attracted interest on several continents, and the people in Europe who made a bankable improvement are not even in the euro zone. First Tobias Mömke and Ola Svensson of KTH in Stockholm obtained by using matchings in place of the more-complicated ingredients of OSS, also in time for FOCS 2011. Then Marcin Mucha of the University of Warsaw improved their analysis to obtain

It is noted by all that an even older paper by Michael Held and Richard Karp from 1970 had set a believable target for provable improvements of Christofides’ bound, namely a conjectured ratio of from linear programming relaxations. However, also has dueling conjectures, some supporting a believable target of . The real point of comparison with TSP is that suddenly there was progress on a barrier that had stood for much of the age of the field, and this attracted others to try for more.

We note that Markus Bläser has contended in a comment that the extension of CW used by both new papers has limitations, and we infer that some other experts concur. However, the paper by Vassilevska Williams in particular has two new ingredients: a framework for managing any tensor power as a base algorithm, and a computer implementation of the framework. She also employed an insight of Stothers to simplify the analysis. Though we can imagine a geometrical insight that higher powers bring returns that “shrink geometrically,” can we really constrain the likelihood that pursuing them might dislodge a different insight that changes the whole game? Is there a limitation theorem here? All we know is that the game has changed, and perhaps the game is afoot.

Worth and Values

The last issue we wish to raise is the reliability of judging the worth of past achievement by present assessment of what it may or may not lead to in the future. We have posted several times on surprises and the difficulty of predicting or guessing how things will go. Of course impetus into the future is necessarily part of claiming something now a “breakthrough.”

However, if we seek a reliable and consistent standard of judging worth, we should use a value that the community has understood for many years: intellectual substance and effort. This value, plus the simple salience of the goal, led our principals to invest the years of work in the first place. Depth of thinking is our gold standard, while applicability is our paper currency. The improvements of and on paper for amid other issues may be a poor return now, but the new computer-assisted vein to mine may parlay true value later.

Dick and I hope this explains why fundamental effort and easily-stated achievement, on a fundamental problem after nearly a quarter-century of stasis, elicited the reaction it has. We agree with, and have tried to extend, Timothy Gowers’ comments here. As for how these values can be invested, only time will be the teller.

Open Problems

Can we be more open about the value of pursuing problems?

What is ?

Suppose we know something special about two matrices and to be multiplied, something not so obvious like their being sparse. Suppose in particular that we have a tiny circuit that for any outputs the value , and similarly for , where those values come from a fixed finite set. Or suppose we know that and/or preserve a similar succinctness property from argument vectors to values—which gives a different property on the part of and . Is this enough to compute faster than what we know for arbitrary matrices?

Quantum mechanics is how nature multiplies matrices. Feynman path integrals (which are fundamental to non relativistic quantum mechanics and relativistic quantum field theory and string theory) are essentially a way of multiplying matrices. And the world is not classical dammit, it’s quantum mechanically, as Feynman reminded us. So if you want a truly fundamental limit, shouldn’t you be including quantum mechanics?

Is there a place I can read the synopsis of what the general idea (including some nice see through details and big picture)? Her paper looks well written but still looks beastly for someone new to the field. Thankyou for the help.

Also say if someone finds 3×3 times 3×3 can be done in 21 steps, would it improve present exponent? If so, by how much?

I guess by your ref to “her paper” you’ve already read our description in the previous post, and of course there’s Stothers’ survey linked in the intro but it gets to brass tacks of the CW method real fast. For brass tacks of other methods, there is this 2008 survey by J.M. Landsberg, which actually has the stuff most of interest to me in all this (polynomial ideals/varieties, quantum, phylogenetics/DNA). Unfortunately Joachim von zur Gathen’s 1988 survey and Strassen’s 1991 survey seem to be behind e-walls; I could dig for others but my kids need this machine. The popular text by Cormen-Leiserson-Rivest(-Stein) has a chapter-or-section(s) devoted mostly to Strassen’s algorithm.

The answer to your second question that simply follows Strassen would be the log-base-3 of 21, which Google tells me is 2.77… Just a little better than 2.807… I don’t know how much more could be based on that—enhancing the basis is the main strategy of the two present papers.

@Interesting work
It turns out that multiplying two 3-by-3 matrices provably takes more than 21 scalar multiplications. However, two 48-by-48 matrices can be multiplied with only 47,217 scalar multiplications, yielding an exponent of 2.7801…

I am too curious not to ask, is it verifiable that Svensson and Mömke were attracted by the OSS result as you suggest? I couldn’t tell from their arXiv version (no mention of “inspired by,” but not “independently” either).

To be clear, in either case both of their results are quite beautiful! And I like hearing more about history and motivation (if accurate)!

We were working on the problem and had some results such as the subcubic case before the announcement of the OSS result.

That said, the OSS result improved the performance guarantee for general graphs and made us more determined to also do that with our approach. So from my perspective, this motivated us to work and think harder.

In short, the techniques are different and independent but the OSS result inspired us to work harder.

Please let me say that for eminently practical reasons this general topic (the computational complexity of linear algebraic systems) is immensely interesting to us simulationists.

It is notable in particular that the Braverman-Makarychev-Makarychev-Naor article expresses a Great Truth: “We chose not to state an explicit new upper bound on the Grothendieck constant since we know that our estimate is suboptimal” which nicely complements the Great Truth that Andrew Stothers and Virginia Vassilevska-Williams both wonderfully contributed to mathematics in providing such upper bounds.

That these opposing great truths can creatively and amicably coexist is (to me) the sign of a healthy culture of mathematics — long may this peaceful coexistence continue!

As a non-specialist, a continuing source of puzzlement (to me anyway) is that steady improvements in upper bounds for algorithms that multiply general matrices are not accompanied by better bounds for solving general linear equations ; the former having complexity for (and decreasing) while the latter has complexity (and seeming stuck at this value (?) ).

Is there some obvious-to-experts reason why the problem of general matrix multiplication is yielding progressive improvements in computational efficiency, while the complexity of solving general linear equations remains fixed at ? If so, what might be that reason? And is the problem of solving general linear equations “pleasantly parallelizable” in a way that helps us understand this discrepancy?

As a followup, the Russian mathematician V. I. Solodovnikov wrote two articles in the late 1970s and early 1980s, titled “The extension of the Strassen estimate to the solution of arbitrary systems of linear equations” (MR538927) and “Upper bounds of complexity of the solution of systems of linear equations” (MR659085) that in essence establish that the direct solution of general systems of linear equations (1) has the same computational complexity as matrix-matrix multiplication and (2) is pleasantly parallelizable. For those of use who burn exaflops of computing power in “sharping” dynamical one-forms to trajectory tangent vectors on large-dimension state-spaces, this doubly favorable scaling is thought-provoking — mathematics and nature conspire to make large-dimension simulation far easier than naively seems possible.

What exactly is the matrix multiplication problem? As defined, it uses symbolic multiplication and treats each entry as a variable, not as a number.

A completely different problem is if we consider matrix multiplication with numbers. Namely, let us suppose that we have to multiply two nxn matrices with integer entries, such that entries are integer numbers taking m bits. Then look at the algorithms for this that take time O(n^c m^d). Then clearly infimum, call it e, over all such c is no greater than your \omega, but the converse is not necessarily true.

In fact, it might be that e=2 is mych easier to obtain – would such restricted matrix multiplication algorithm be of any value (theoretical/practical – would you call it breakthrough)? Are there any inequalities for e (the restricted number matrix complexity exponent) that are better than the general purpose inequalities for your \omega?

The article is correct as written. To compare, I’ve been thinking about what should be the “correct” measure of N-partite quantum entanglement since 2002, decided in late 2007 that polynomial-ideal invariants might furnish such a measure, worked on it while on sabbatical in 2009, but the 2008 survey by J.M. Landsberg (which I found to answer a comment above) gives me a fresh pointer on it—see page 13. What was your point and purpose, anyway?

Omega is a good example of an uncomputable number: for us to know its value, it would imply we can travel to the future and see what new algorithms have been invented. I agree that it’s elegant to define it as the infimum of all c such that nXn matrix multiplication has an O(n^c) algorithm, but once you’ve said this you can’t prove anything about it. You know that a lower bound exists, period. The only way of getting closer to it is coming up with a better algorithm for the same problem. IMHO, the time it takes scientists to get closer and closer to Omega is a much more accurate indicator of the hardness of matrix multiplication, than the value of Omega itself.

On a related, albeit possibly obvious, note, with O(n^3) classical processing hardware, one can multiply two n x n matrices in O(log n) time. Despite being fairly obvious, it seems to get overlooked in some papers talking about using a polynomial amount of quantum processing hardware to perform matrix operations in polylogarithmic time, which is made decidedly less notable by the classical result.